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REVIEW 2 major objections 4 minor 120 references

Small Foundation Models of Human Cognition and Behaviour

T0 review · 2 major / 4 minor · reviewed 2026-08-08 · deepseek-v4-flash

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Pith's one-line read Within the 160 experiments of Psych-101, 0.6B-to-1B parameter models match a 70B baseline on held-out participants; scale matters only for transfer to unseen paradigms, and ablations show predictions rest on stimulus content, not…

desk verdict Solid scaling and ablation results with an honest but load-bearing caveat: the in-distribution plateau is plausibly a data noise ceiling, but the paper cannot rule out that it is an SFT/LoRA ceiling. read the letter →

arxiv 2608.05224 v1 pith:YUK5EAFQ submitted 2026-08-05 cs.AI cs.CY

Nick Oh , Fernand Gobet This is my paper · ORCID
classification cs.AIcs.CY
keywords cognitivefoundationmodelsnoiseceilingmodelscalepromptablationbehaviouralpredictiontransferlearningshortcutpsychologyexperiments
verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

The paper takes two open questions about fine-tuned language models as cognitive proxies — how much scale they need, and whether they use task structure or exploit statistical shortcuts — and answers both with experiments across fourteen models from 135M to 14B parameters. On held-out participants from the same 160 experiments used for training, the models cluster in a narrow band and 0.6B-1B parameters suffice to match a 70B baseline, so in-distribution accuracy is not what large scale buys. On eighteen held-out experiments, larger models are clearly better, so scale buys transfer to novel task structure. Prompt ablations across 27 experiments show that masking the content of stimuli and feedback destroys 75.7% of learned information and pushes the models below chance, ruling out choice history alone. The upshot, if right, is that small cognitively fine-tuned models can serve as cheap noise-ceiling estimators for psychology experiments, with their reach bounded by the paradigms in the training data.

What carries the argument

The carrying instrument is the four-channel decomposition of the training objective, $P(C_{t+1}\mid I, S_{1:t+1}, F_{1:t}, C_{1:t})$, which separates task instructions ($I$), upcoming and past stimuli ($S$), outcome feedback ($F$), and the participant's choice history ($C$). The content-masked ablation is the discriminating probe: it replaces specific stimulus values and feedback outcomes with generic placeholders while preserving trial format, so any drop in accuracy is attributable to informational content rather than to the template. Information retention is measured by $R = (\ln k - \mathrm{NLL}_{\mathrm{ablation}}) / (\ln k - \mathrm{NLL}_{\mathrm{original}})$, with $k$ response options, which yields the paper's partition of lost information (75.7% content, 12.5% instruction, 11.7% template). The other half of the machinery is the adapter-rank sweep, which shows that 0.6B-1B parameter models at high rank match the 70B baseline at low rank, establishing that in-distribution accuracy is capacity-independent.

What would settle it

Train the same small models with full fine-tuning or a reinforcement-learning objective on the same corpus; if the narrow band narrows further or shifts below the current 0.5-nats floor, the plateau belongs to the supervised objective, not to human unpredictability, and the noise-ceiling reading fails.

Watch

Extended reading notes

Core claim

The central discovery is an in-distribution ceiling with an out-of-distribution slope. Fourteen models from four base-model families, from 135M to 14B parameters, are fine-tuned on Psych-101, a corpus of 10.7 million trial-level choices from 160 experiments, using rank-stabilised low-rank adapters. On held-out participants within those experiments the eight matched models span only 0.028 nats of mean negative log-likelihood, from 0.509 to 0.537, a band that contains the reproduced 70B baseline, and the parameter count needed to match that baseline falls from 8B at adapter rank 4 to 0.6B at rank 32; fine-tuning itself contributes roughly ten times more than scale. On eighteen held-out experiments from Psych-201, the same models spread across 0.244 nats, with the largest model in each family clearly best. Under prompt decomposition, removing instructions costs 12.5% of learned information, masking the content of stimuli and feedback costs 75.7% and sends models below chance, and the trial template accounts for 11.7%; permutation tests show order-invariance on an exchangeable similarity task and order-sensitivity on an adaptive choice task. The paper concludes that small cognitively fine-tuned transformers are adequate noise-ceiling estimators within the paradigms they were trained on, with capacity limiting transfer rather than in-distribution fit.

Load-bearing premise

The entire claim depends on the assumption that the flat performance band on familiar tasks comes from genuine randomness in human behaviour, not from a ceiling imposed by the supervised fine-tuning method itself — the paper explicitly says it cannot rule out the latter.

Editorial extensions

If this is right

  • Computing budgets for behavioural foundation models can drop by roughly two orders of magnitude for in-distribution use: a 0.6B model with a high-rank adapter matches a 70B baseline trained and evaluated under the same protocol.
  • Scale and money should be spent on out-of-distribution transfer, since the scaling gradient on unseen experiments is steep and shows no saturation within the sizes tested.
  • A noise-ceiling estimate from these models is only as broad as the training corpus: for paradigms inside Psych-101 it is informative, for paradigms outside it is unvalidated.
  • The shortcut hypothesis is refuted in its strong and format-only forms for sequential tasks: choice history alone performs below chance on average, and masking content destroys most of the learned information.
  • New training data should add breadth (new experimental paradigms) rather than depth (more participants), since returns per additional participant are already diminishing within covered paradigms.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

  • The authors' own caveat suggests a decisive test of the ceiling interpretation: if full fine-tuning or a reinforcement-learning objective on the same corpus pulls the in-distribution band below 0.5 nats, part of the 'noise ceiling' belongs to the supervised objective, not to human unpredictability.
  • The exchangeability diagnostic could be turned into a general validation protocol for cognitive proxies: before trusting a model on a task, check that its sensitivity to trial order matches the task's contingency structure.
  • Cross-task datasets where the same participants complete several paradigms would let ceiling estimates separate person-level stability from task-level predictability, a decomposition the paper notes is currently impossible.
  • If the plateau is data-derived, other behavioural datasets could be mined similarly: train a small fine-tuned model, measure the ceiling, and use the gap between it and interpretable theories as a map of where theory-building has the most room to improve.
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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Referee Report

2 major / 4 minor

Summary. The paper trains fourteen small language models (135M-14B parameters) across four architecture families with rank-stabilised LoRA on the Psych-101 dataset and compares them against a reproduced Centaur-70B baseline. It reports that in-distribution predictive performance is nearly flat in model size, with 0.6B-1B models matching Centaur-70B on held-out participants once adapter rank is sufficiently high, while out-of-distribution performance on Psych-201-RT retains a clear scaling gradient. The paper then decomposes the prompt into instruction, stimuli, feedback, and choice-history channels, showing that content-masking destroys most learned information, and pairs this with order-permutation tests on one exchangeable and one adaptive task. The authors conclude that small cognitively fine-tuned models can serve as noise-ceiling estimators within trained paradigms, provided their predictions rest on the content participants actually saw.

Significance. The empirical contributions are solid and useful. The scale/rank/data decomposition is clean, the Centaur-70B reproduction reported in Appendix C.3 (r=0.994) is a genuine reproducibility asset, per-experiment results are provided for all 46 Psych-101 and 18 Psych-201 experiments, and the content-masking ablation is a methodological step beyond the four-experiment shortcut studies in prior work. If the noise-ceiling interpretation survives, the paper makes a strong practical case that small cognitively fine-tuned transformers are inexpensive estimators of predictable behavioural structure. The principal caveat is that the in-distribution plateau is observed only under LoRA adaptation; the paper itself flags this in Sections 4.1.2 and 6, and the central 'noise ceiling' label depends on resolving it.

major comments (2)
  1. [Sections 4.1.2, 5, and 6] The central claim that small models are noise-ceiling estimators assumes that the in-distribution plateau (0.509-0.537 at rank 16) is a property of the behavioural data rather than of the rank-stabilised LoRA training regime. All fourteen models use LoRA with r at most 64, and the 70B baseline is 4-bit QLoRA, so the plateau could be an adapter ceiling. Section 4.1.1 itself shows that Qwentaur-0.6B improves from 0.528 at r=16 to 0.513 at r=64, so the band moves with adapter capacity. Section 6 acknowledges that full fine-tuning at small scales would separate a genuine data ceiling from a low-rank adaptation ceiling. Because the licence argument in Section 5 uses content use to justify treating the models as ceilings, and content use is necessary but not sufficient for that conclusion, this is a load-bearing unresolved confound. The manuscript should either run full fine-tuning on at least one small model, such as Qwen3-0.6B, and show that in-distribution NLL does not fall materially below the LoRA band, or systematically replace the 'noise ceiling' language with 'low-rank SFT bound' and restrict the claims accordingly.
  2. [Section 4.2.3] The task-adaptive information use conclusion rests on exactly two permutation experiments, one primary exchangeable task and one adaptive negative control, and the text notes that only one exchangeable task is available in Psych-101. The variance and ECDF plots in Figure 5 are descriptive; no significance test, effect size, or confidence interval is reported for the fine-tuned versus base model variance difference on THINGS odd-one-out. Since this result is used in the Discussion to support the interpretation that the models respect exchangeability rather than defaulting to sequential heuristics, a quantitative summary of the permutation variance comparison, or additional exchangeable tasks where available, would materially strengthen the claim.
minor comments (4)
  1. [Figures 1, 2, 4, and 5] The axis labels and legend text in several figures render as corrupted character codes in the submitted PDF; please repair the font embedding or vector text so that the figures are readable.
  2. [Abstract and Section 4.1.1] The abstract states that '0.6B to 1B parameters suffice to match a 70B baseline' without the qualifier that this holds at LoRA ranks 32-64 on the full training set; adding that qualifier would make the claim more precise.
  3. [Section 4.2.2] The retention statistic R is defined with ln k as the chance level, but the per-experiment figure caption excludes experiments with delta > 1 under the history-only condition; please clarify whether the mean retention reported in Figure 4a includes those experiments or only the subset shown in Figure 4b.
  4. [Appendix C.3] The Centaur-70B reproduction has mean deviation +0.024 nats from the published values; while modest, this difference is in the direction of making the 'matching' threshold slightly easier, and it would be useful to state explicitly that the rank-sweep matching conclusions are robust to this mean offset.

Circularity Check

0 steps flagged · score 1.0 of 10

No significant circularity: the central claims are direct measurements, and the noise-ceiling interpretation is explicitly hedged against a method-ceiling alternative.

full rationale

The paper's central claims are empirical measurements rather than derivations. (i) The in-distribution plateau is a directly evaluated held-out NLL band across fourteen independently trained LoRA adapters (Section 4.1.1). (ii) The claim that smaller models match the Centaur-70B baseline is read off a rank sweep (Figure 1), and Centaur-70B itself is independently reproduced under matched software conditions (Appendix C.3) rather than taken on citation. (iii) The content-use claim rests on a new diagnostic, the content-masked condition (Section 4.2.1), whose retention metric R is computed directly from NLL; no parameter is fitted on the evaluation set and later relabeled as a prediction, and the 75.7% figure is a direct partition of measured retention drops, not a fitted quantity. The one load-bearing interpretive step is naming the plateau a noise ceiling, and there the paper does the opposite of what a circular argument would do: Section 4.1.2 states 'Psych-101 may contain structure that supervised fine-tuning on next-choice prediction is unable to extract, in which case the limit belongs to the method rather than the data,' and Section 6 states 'Full fine-tuning at the smallest scales would separate a genuine ceiling on the learnable signal from one imposed by low-rank adaptation.' The LoRA-versus-data-ceiling confound is thus disclosed as an open question rather than assumed away, so the ceiling inference is a hedged empirical conjecture, not an equation that reduces to its inputs. Self-citations (Gobet et al. 2001; Simon & Gobet 2000; Gobet & Ritter 2000) are background and limitation-context references and are not load-bearing for any main result; the load-bearing external inputs (Psych-101 data, prompt templates, cognitive baselines) come from Binz et al. (2025), an independent prior work, and from the paper's own training runs. Remaining reviewer concerns are correctness and validity risks, not circularity: all fourteen models and the 70B baseline use LoRA/QLoRA, so the plateau could be an adapter ceiling (explicitly acknowledged by the paper), and the abstract's '0.6B to 1B suffices' threshold holds at r>=32 while the reference configuration is r=16. Neither makes any claim true by construction or by definition.

Assumptions & free parameters 1 free parameters · 4 assumptions · 0 invented entities

The central claims rest on the imported premises above; no new particles, forces, dimensions, or mechanistic entities are introduced. The only fitting in the paper is descriptive (trend lines in Figures 1-2, and the interpolation of the size needed to match Centaur-70B), neither of which enters the ablation or transfer claims as a fitted constant.

free parameters (1)
  • No free parameters fitted for the central claims
    The headline results are measurements (NLL bands, retention R, permutation variance). The size needed to match 70B (8B at r=4, 0.6B at r=32) is interpolated from the LoRA-rank sweep, not a fitted constant; trend lines in Figures 1-2 are descriptive fits within matched families and are not used to define the claims.
assumptions (4)
  • domain assumption Psych-101 train-test splits and prompt templates faithfully encode the experimental structure as used by Centaur.
    Section 3 states the paper uses the same splits and templates without modification; all in-distribution claims inherit this fidelity assumption.
  • domain assumption A well-trained neural model's held-out NLL lower-bounds achievable prediction, i.e., the noise-ceiling logic.
    Imported from Agrawal et al. (2020) and Kuperwajs et al. (2023) in Sections 1 and 2.1; the paper's final interpretation depends on it.
  • domain assumption Mean NLL over the 38 Psych-101 tasks with published cognitive baselines is a valid aggregate for judging model equivalence.
    Section 4.1 and Appendix C.1 exclude 8 or 12 tasks with continuous, mixed, or degenerate action spaces; the 70B-match claim is defined on this subset.
  • ad hoc to paper THINGS odd-one-out and intertemporal choice are representative anchors of exchangeable versus adaptive task structure.
    Section 4.2.3 selects these two experiments as primary test and negative control; the exchangeability conclusion generalizes only if they represent their classes.

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Cite this review

Pith. "Pith review of Small Foundation Models of Human Cognition and Behaviour." pith.science (2026). https://pith.science/paper/YUK5EAFQ

@misc{pith2026260805224,
  author       = {Pith},
  title        = {Pith review of: Small Foundation Models of Human Cognition and Behaviour},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/YUK5EAFQ}},
  note         = {Machine review of arXiv:2608.05224}
}
read the original abstract

Large language models fine-tuned on human behavioural data have emerged as general-purpose cognitive proxies, but the scale this requires, and whether these models process task structure or exploit statistical shortcuts, remain open questions. We train fourteen models from 135M to 14B parameters across four architecture families on Psych-101, a dataset of 10.7 million trial-level choices from 160 experiments. In-distribution, scale barely matters. The models fall within a narrow band, as though against a ceiling, and 0.6B to 1B parameters suffice to match a 70B baseline on held-out participants. Out-of-distribution, that band opens into a markedly steeper scaling gradient, with larger models clearly advantaged in generalisation to novel task structure. To determine what information these models use, we run two diagnostics. We progressively strip four prompt channels -- task instructions, experimental stimuli, outcome feedback, and choice history -- across 27 experiments, and permute trial order. Masking the content of stimuli and feedback destroys 75.7% of learned information and pushes models below chance, demonstrating that choice history alone does not account for performance. Permutation reveals invariance on tasks with independent trials but sensitivity where trial order is determined by prior responses. Small cognitively fine-tuned models therefore show promise as noise ceiling estimators for psychological experiments, though their scope remains bounded by the paradigms seen in training.

Figures

Figures reproduced from arXiv: 2608.05224 by the authors.

Figure 1
Figure 1. Adapter rank against model size on Psych-101. Mean negative log-likelihood over the 38 of 46 Psych-101 tasks for which Binz et al. (2025) publish a domain-specific cognitive model, plotted against parameter count, one panel per adapter rank (r = 4–64). Trend lines are fitted only within groups matched on generation and context window, so Olmotaur has none and the Smoltaur fit covers the SmolLM2 models only. 10 1 10 … view at source ↗
Figure 2
Figure 2. In-distribution versus out-of-distribution scaling at rank 16. (a) Psych-101, mean NLL over the 38 tasks with a reported cognitive model. (b) Psych-201-RT, all 18 held-out experiments; no cognitive baseline is published for Psych-201. Trend lines are fitted only within groups matched on generation and context window. Centaur-70B moves accordingly, from 8B at r=4 to 3B at r=8, 1.7B at r=16, and 0.6B at r=32 and above… view at source ↗
Figure 3
Figure 3. Prompt decomposition into four information channels. (Left) Example prompt from Psych-101 (Binz et al., 2025) with channels colour-coded. (Right) Ablation conditions and their effective prediction objectives. Per-experiment prompts under all four ablation conditions are shown in Figures 19–50 (Appendix F.2). with generic placeholders (e.g. “some points”, “a shape”) and reduces the instruction to a minimal action-spa… view at source ↗
Figures from the paper (49 more)
Figure 4
Figure 4. Figure 4: Structural ablation results across eight models and 27 experiments with well￾defined response options. Five experiments with mixed or continuous formats are excluded. (a) Mean information retention R = (ln k − Lc)/(ln k − Lorig) by condition, averaged over experiments;…
Figure 5
Figure 5. Figure 5: Per-participant order variance across models and experiments. (a) THINGS odd-one-out (exchangeable; primary test). (b) Intertemporal choice (adaptive staircase; negative control). Left: violin and box plots; fine-tuned (solid) vs. base (hatched); y-axis scales differ. …
Figure 6
Figure 6. Figure 6: Adapter rank against model size on Psych-101. Mean negative log-likelihood over the 38 of 46 Psych-101 tasks for which Binz et al. (2025) publish a domain-specific cognitive model baseline, against parameter count, with colour intensity encoding LoRA rank and right-han…
Figure 7
Figure 7. Figure 7: Adapter rank and training-set size by family. (Left) Mean NLL against LoRA rank at full data. (Right) Mean NLL against the fraction of Psych-101 used for training, at r=16. Rows are the four model families; the dotted line is the cognitive-model baseline and the diamon…
Figure 8
Figure 8. Figure 8: Reproducibility of Centaur-70B (4-bit) evaluation across Psych-101. Reproduced vs. reported NLL for Centaur-70B (4-bit) across 46 Psych-101 experiments (r = 0.994, mean ∆ = +0.024, median ∆ = +0.006). Centaur-70B (Binz et al., 2025) uses QLoRA with a frozen 4-bit quant…
Figure 9
Figure 9. Figure 9: Specificity of cognitive fine-tuning: comparison with non-cognitive control mod￾els. Mean NLL on Psych-101 for cognitively fine-tuned models (Llama-Centaur, Qwentaur; LoRA r=16, full training data) and size-matched non-cognitive and cognitive controls (Hermes, Nemotron…
Figure 10
Figure 10. Figure 10: Impact of cognitive fine-tuning on MetaBench performance (∆ = fine-tuned − base). Each bar shows the change in accuracy for a matched base–fine-tuned pair on six standard LM benchmarks (ARC, GSM8K, HellaSwag, MMLU, TruthfulQA, Winogrande) plus their mean. Error bars s…
Figure 11
Figure 11. Figure 11: Impact of cognitive fine-tuning on Ethics benchmark performance (∆ = fine￾tuned − base). Each bar shows the change in accuracy for a matched base–fine-tuned pair across five ethical reasoning tasks (commonsense morality, deontology, justice, utilitarianism, virtue) pl…
Figure 12
Figure 12. Figure 12: Impact of cognitive fine-tuning on cognitive and language benchmark per￾formance (∆ = fine-tuned − base). Each bar shows the change in accuracy for a matched base–fine-tuned pair across six tasks (LogiQA, PIQA, Social IQA, CoQA, LAMBADA￾OpenAI, LAMBADA-Standard) plus …
Figure 13
Figure 13. Figure 13 [PITH_FULL_IMAGE:figures/full_fig_p044_13.png]
Figure 14
Figure 14. Figure 14: Multi-armed bandits: Spatially correlated multi-armed bandit (Wu et al., 2018), as ablated by Xie & Zhu (2025). Removed are the rationale of the task, the reward structure, and every feedback statement. What survives is the action space, a repeated block marker, and t…
Figure 15
Figure 15. Figure 15: Supervised learning: Multiple-cue judgment (Collsio¨o et al. ¨ , 2023), as ablated by Xie & Zhu (2025). Here the cue values are the task, so deleting them removes any basis for a judgement and leaves a sequence of numbers drawn from a nine-item response set. This is o…
Figure 16
Figure 16. Figure 16: Decision-making: Multi-attribute decision-making (Hilbig & Moshagen, 2014), a non-sequential task, as ablated by Xie & Zhu (2025). The zero-shot condition (lower right) retains the task in full and removes the choice history, so each trial is predicted in isolation an…
Figure 17
Figure 17. Figure 17: Decision-making: Gardening task (Flesch et al., 2018), as ablated by Liu & Ding (2025). Instruction free is our instruction-ablated condition and context free is our choice-only condition. The misleading instruction removes no information but supplies an instruction c…
Figure 18
Figure 18. Figure 18: Complete per-experiment ablation heatmaps for 26 experiments with a well￾defined chance baseline. Five additional experiments with mixed or continuous response formats are excluded throughout because no single k defines a chance baseline. The proba￾bilistic instrument…
Figure 19
Figure 19. Figure 19: Supervised learning: Shepard categorization (Badham et al., 2017). 52 [PITH_FULL_IMAGE:figures/full_fig_p052_19.png]
Figure 20
Figure 20. Figure 20: Multi-armed bandits: Drifting four-armed bandit (Bahrami et al., 2020). 53 [PITH_FULL_IMAGE:figures/full_fig_p053_20.png]
Figure 21
Figure 21. Figure 21: Supervised learning: Multiple-cue judgment (Collsio¨o et al. ¨ , 2023). 54 [PITH_FULL_IMAGE:figures/full_fig_p054_21.png]
Figure 22
Figure 22. Figure 22: Multi-armed bandits: Horizon task (Feng et al., 2021). 55 [PITH_FULL_IMAGE:figures/full_fig_p055_22.png]
Figure 23
Figure 23. Figure 23: Decision-making: Columbia card task (Frey et al., 2017). 56 [PITH_FULL_IMAGE:figures/full_fig_p056_23.png]
Figure 24
Figure 24. Figure 24: Decision-making: Experiential-symbolic task (Garcia et al., 2023). No retention ratio or chance baseline is shown because trials mix binary choices with continuous proba￾bility estimates, so no single k defines a uniform-guessing floor. 57 [PITH_FULL_IMAGE:figures/fu…
Figure 25
Figure 25. Figure 25: Multi-armed bandits: Two-armed bandit (Gershman, 2018). 58 [PITH_FULL_IMAGE:figures/full_fig_p058_25.png]
Figure 26
Figure 26. Figure 26: Decision-making: Risky choice (Krueger et al., 2024). No retention ratio or chance baseline is shown because trials span multiple stages with varying numbers of actions, so no single k defines a uniform-guessing floor. 59 [PITH_FULL_IMAGE:figures/full_fig_p059_26.png]
Figure 27
Figure 27. Figure 27: Multi-armed bandits: Prob. instrumental learning (Lefebvre et al., 2017). 60 [PITH_FULL_IMAGE:figures/full_fig_p060_27.png]
Figure 28
Figure 28. Figure 28: Decision-making: choices13k (Peterson et al., 2021). 61 [PITH_FULL_IMAGE:figures/full_fig_p061_28.png]
Figure 29
Figure 29. Figure 29: Decision-making: CPC18 (Plonsky et al., 2018). 62 [PITH_FULL_IMAGE:figures/full_fig_p062_29.png]
Figure 30
Figure 30. Figure 30: Multi-armed bandits: Horizon task (Sadeghiyeh et al., 2020). 63 [PITH_FULL_IMAGE:figures/full_fig_p063_30.png]
Figure 31
Figure 31. Figure 31: Multi-armed bandits: Structured bandit (Schulz et al., 2020). 64 [PITH_FULL_IMAGE:figures/full_fig_p064_31.png]
Figure 32
Figure 32. Figure 32: Multi-armed bandits: Horizon task (Somerville et al., 2017). 65 [PITH_FULL_IMAGE:figures/full_fig_p065_32.png]
Figure 33
Figure 33. Figure 33: Supervised learning: Weather prediction task (Speekenbrink et al., 2008). 66 [PITH_FULL_IMAGE:figures/full_fig_p066_33.png]
Figure 34
Figure 34. Figure 34: Multi-armed bandits: Iowa gambling task (Steingroever et al., 2015). 67 [PITH_FULL_IMAGE:figures/full_fig_p067_34.png]
Figure 35
Figure 35. Figure 35: Multi-armed bandits: Horizon task (Waltz et al., 2020). 68 [PITH_FULL_IMAGE:figures/full_fig_p068_35.png]
Figure 36
Figure 36. Figure 36: Multi-armed bandits: Horizon task (Wilson et al., 2014). 69 [PITH_FULL_IMAGE:figures/full_fig_p069_36.png]
Figure 37
Figure 37. Figure 37: Supervised learning: Aversive learning (Wise et al., 2019). No retention ratio or chance baseline is shown because responses are continuous probability estimates, so no single k defines a uniform-guessing floor. 70 [PITH_FULL_IMAGE:figures/full_fig_p070_37.png]
Figure 38
Figure 38. Figure 38: Multi-armed bandits: Spatially correlated MAB (Wu et al., 2018). 71 [PITH_FULL_IMAGE:figures/full_fig_p071_38.png]
Figure 39
Figure 39. Figure 39: Decision-making: Decisions from description (Wulff et al., 2018). 72 [PITH_FULL_IMAGE:figures/full_fig_p072_39.png]
Figure 40
Figure 40. Figure 40: Multi-armed bandits: Decisions from experience (Wulff et al., 2018). No retention ratio or chance baseline is shown because trials mix sample, stop, and choose phases with different response formats, so no single k defines a uniform-guessing floor. 73 [PITH_FULL_IMAG…
Figure 41
Figure 41. Figure 41: Multi-armed bandits: Changing bandit (Xiong et al., 2023). 74 [PITH_FULL_IMAGE:figures/full_fig_p074_41.png]
Figure 42
Figure 42. Figure 42: Decision-making: Gardening task (Flesch et al., 2018). 75 [PITH_FULL_IMAGE:figures/full_fig_p075_42.png]
Figure 43
Figure 43. Figure 43: Supervised learning: Conditional associative learning (Collins et al., 2014). 76 [PITH_FULL_IMAGE:figures/full_fig_p076_43.png]
Figure 44
Figure 44. Figure 44: Decision-making: Multi-attribute decision (Hilbig & Moshagen, 2014). 77 [PITH_FULL_IMAGE:figures/full_fig_p077_44.png]
Figure 45
Figure 45. Figure 45: Supervised learning: Medin categorization (Levering et al., 2020). No retention ratio or chance baseline is shown because trials mix binary classification with 9-point rating responses, so no single k defines a uniform-guessing floor. 78 [PITH_FULL_IMAGE:figures/full…
Figure 46
Figure 46. Figure 46: MDP: Model-based two-step task (Kool et al., 2016). 79 [PITH_FULL_IMAGE:figures/full_fig_p079_46.png]
Figure 47
Figure 47. Figure 47: MDP: Two-step effort cost (Kool et al., 2017). 80 [PITH_FULL_IMAGE:figures/full_fig_p080_47.png]
Figure 48
Figure 48. Figure 48: MDP: Two-step with aliens (Zorowitz & Niv, 2023). 81 [PITH_FULL_IMAGE:figures/full_fig_p081_48.png]
Figure 49
Figure 49. Figure 49: MDP: Subway navigation (Tomov et al., 2020). 82 [PITH_FULL_IMAGE:figures/full_fig_p082_49.png]
Figure 50
Figure 50. Figure 50: MDP: Multi-task reinforcement learning (Tomov et al., 2021). 83 [PITH_FULL_IMAGE:figures/full_fig_p083_50.png]
Figure 51
Figure 51. Figure 51: Miscellaneous: THINGS odd-one-out (Hebart et al., 2023). Original In the following you will be presented with multiple choices between two options Q and L. Please name which option you would prefer by pressing the corresponding key. You have the choice between receivi…
Figure 52
Figure 52. Figure 52: Decision-making: Intertemporal choice (Ruggeri et al., 2022). 84 [PITH_FULL_IMAGE:figures/full_fig_p084_52.png]

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Pith tools

Reviewed August 8, 2026 · model on record in the stance chip above.